Finance and Economics Discussion SeriesDivisions of Research & Statistics and Monetary Affairs

Federal Reserve Board, Washington, D.C.

Do Creditor Rights Increase Employment Risk? Evidence fromLoan Covenants

Nellie Liang and Antonio Falato

2014-61

NOTE: Staff working papers in the Finance and Economics Discussion Series (FEDS) are preliminarymaterials circulated to stimulate discussion and critical comment. The analysis and conclusions set forthare those of the authors and do not indicate concurrence by other members of the research staff or theBoard of Governors. References in publications to the Finance and Economics Discussion Series (other thanacknowledgement) should be cleared with the author(s) to protect the tentative character of these papers.

Do Creditor Rights Increase Employment Risk?

Evidence from Loan Covenants

Antonio Falato

Federal Reserve Board

Nellie Liang1

Federal Reserve Board

This draft: October 2013

1Views expressed are those of the authors and do not represent the views of the Board or its staff. Con-tacts: antonio.falato@frb.gov, jnellie.liang@frb.gov. Special thanks to Mark Carey and Greg Nini for theirhelp with Dealscan and for kindly sharing their Compustat-Dealscan key. We thank Bill Bassett, SudheerChava (discussant), Edward Morrison (discussant), Greg Nini, Marco Pagano, Michael Roberts (discus-sant), Steve Sharpe, Martin Schmalz, Amir Sufi; seminar participants at the Federal Reserve Board; andconference participants at the annual meetings of the American Economic Association, American FinanceAssociation, and the Conference on Empirical Legal Studies for helpful comments and discussions. Bran-don Nedwek, Nicholas Ryan, Richard Verlander, and especially Suzanne Chang provided excellent researchassistance. All remaining errors are ours.

Abstract

Using a regression discontinuity design, we provide evidence that incentive conflicts between

firms and their creditors have a large impact on employees. There are sharp and substantial em-

ployment cuts following loan covenant violations, when creditors exercise their ex post control

rights. The negative impact of violations on employment is stronger for firms that face more severe

agency and financing frictions and those whose employees have weaker bargaining power. Em-

ployment cuts following violations are much larger during industry and macroeconomic down-

turns, when employees have fewer alternative job opportunities and reduced bargaining power.

Union elections that create new labor bargaining units lead to higher loan spreads, consistent with

creditors requiring compensation for their reduced control rights when labor is stronger. Overall,

these findings enrich our understanding of the consequences of the state contingent transfer of

control rights by identifying a risk-shifting channel from creditors to employees. Our analysis es-

tablishes an endogeneity-free link between financing frictions and employment and offers direct

evidence that binding financial covenants are an important amplification mechanism of economic

downturns.

1 Introduction

One fundamental contribution of modern corporate finance is the insight by Jensen and Meckling

(1976) that firms are a complex nexus of contractual relations.1 Important aspects of this orig-

inal insight have been developed. In particular, the literature has extensively studied conflicts

of interest between shareholders and managers and between shareholders and debtholders (see

Stein (2003) for a survey). It is now well understood that these conflicts of interest can poten-

tially be mitigated by contractual features such as, for example, financial covenants that protect

lenders before non-payment or default by defining a state-contingent transfer of control rights. A

growing recent empirical literature (Chava and Roberts (2008), Roberts and Sufi (2009), and Nini,

Smith and Sufi (2009, 2012)) shows that loan covenants are indeed effective at protecting creditors’

rights, and that the transfer of control rights that accompanies covenant violations has important

consequences for firm investment and financial policies.

Another important insight of the nexus of contracts view has received relatively little atten-

tion. There can also be a fundamental conflict of interest between creditors and other stakeholders

stemming from the fact that each of these groups has a priority claim on firm revenues. In Jensen

and Meckling (1976), “firms incur obligations daily to suppliers, to employees, to different classes

of investors, etc. So long as the firm is prospering, the adjudication of claims is seldom a problem.

When the firm has difficulty meeting some of its obligations, however, the issue of the priority

of those claims can pose serious problems.” Since a complex web of multiple contracts ultimately

determine the adjudication of claims, the allocation of rights between shareholders and credi-

tors likely has an impact on contractual relations between the firm and nonfinancial stakeholders.

However, we have virtually no empirical evidence on whether and how creditor rights actually

impact nonfinancial stakeholders.

1"There is in a very real sense only a multitude of complex relationships (i.e., contracts) between the legal fiction(the firm) and the owners of labor, material and capital inputs and the consumers of output. The firm [. . . ] is a legalfiction, which serves as a focus for a complex process in which the conflicting objectives of individuals (some of whommay “represent” other organizations) are brought into equilibrium within a framework of contractual relations. In thissense the “behavior” of the firm is [...] the outcome of a complex equilibrium process." (Jensen and Meckling (1976))

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In an attempt to fill the gap in the literature, this paper examines conflicts of interest between

creditors and an important class of nonfinancial stakeholders. Specifically, we assess the impact

of loan covenant violations on employees. Why would covenant violations affect employees?

Loan covenants which are tied to performance indicators protect creditors by defining a transfer

of control rights when a covenant is violated (e.g., financial contracting theory of Aghion and

Bolton (1992) and Dewatripont and Tirole (1994)). Such violations provide creditors with the same

rights as would payment defaults, including the ability to accelerate any outstanding principal

and to terminate any unused revolving credit facility, and lead to renegotiation of loans on less

favorable terms to borrowers. In order to avoid acceleration and ensure continued access to credit,

management may decide to reduce operating costs by cutting jobs after a covenant violation in an

attempt to reassure creditors about the firm’s ability to generate cash flows. Employees may also

be affected directly by creditors’ interventions in the form of “advising” management to reduce

headcount and operating expenses, as exemplified by the following excerpt from the first quarter

10-Q filing of Interpharm Holdings in 2008:2

Subsequently, on January 28, 2008, Wells Fargo informed the Company that it wouldconsider providing the Company with credit availability on the condition that theCompany (i) develops and implements a new operating plan focused on increasing theamount of eligible collateral and reducing costs and (ii) develop an alternative financ-ing arrangement. Further, on February 5, 2008, the Company and Wells Fargo enteredinto the Forbearance Agreement [. . . ] In connection with its negotiation of the Forbear-ance Agreement, the Company completed a restructuring of its operations on January25, 2008 and submitted a new operating plan to Wells Fargo, which the Company be-lieves will result in positive cash flow and net profits, and includes [. . . ] reducingpayroll and headcount by approximately 20%.

Consistent with this reasoning, we document large-sample evidence that loan covenant viola-

tions and the associated transfer of control rights to creditors lead to less job security for workers.

2Using keyword searches of SEC filings (with keywords such as employee or headcount or overhead reduction)we found several cases of a direct link between violations and employement in management discussion of violations.For instance, the annual 10-K filing of Meade Instruments Corp in 2008 reads as follows: "We are working with ourlender on a potential amendment to our agreement to cure this technical default. Our restructuring plans includeimplementation of headcount reductions, corporate overhead and manufacturing costs." From the second quarter 10-Qfiling of Advanced Materials in 2004: "The Company is in the process of attempting to cure its line of credit and termloan violations. Management has implemented a plan to reduce expenses and improve sales. Selling, general andadministrative expenses for the first quarter of fiscal 2004 and 2003 were $397,000 and $499,000, respectively, a decreaseof $102,000 or 20%. This decrease was due primarily to a reduction in the number of employees as the Companycontinues to improve individual productivity."

2

Ours is the first endogeneity-free evidence that financing frictions have a sizable adverse impact

on employment and that binding contractual covenants are an amplification mechanism of down-

turns. This evidence contributes to the classical academic and policy debate on the influence of

corporate financing on macroeconomic and financial stability (e.g., Bernanke and Gertler (1989);

Sharpe (1994), Hanka (1998), Benmelech, Bergman, and Seru (2011), and Pagano and Pica (2011)

focus on employment), a debate which has been recently revived in the aftermath of the financial

crisis and the ensuing Great Recession of 2008 and 2009.

Specifically, we use a regression discontinuity design pioneered by Chava and Roberts (2008)

to achieve identification and document sizable job cuts following a loan covenant violation, which

are concentrated among firms with agency problems and whose employees have weak bargain-

ing power.3 Our sample consists of 11,536 firm-year observations for 2,265 unique US firms that

have information on loan covenants in Dealscan and on employment and firm balance-sheet in

Compustat between 1994 and 2010, which we complement with 3,129 hand-collected layoff an-

nouncements from major news sources to construct measures of employment that do not reflect

workers’ voluntary separations.4 Our baseline estimates indicate that employment falls sharply in

response to a covenant violation by about 18% per year, a reduction which is roughly three times

as large as the median employment drop in the sample. The estimates are robust to restricting the

sample to include only observations that are "close" to the covenant threshold, where violations

can be plausibly considered a "quasi-random" treatment.5

Employment cuts subsequent to violations become as deep as 30% per year for firms with more

severe agency problems, and as much as 27% for firms whose employees have weaker bargain-

ing power. Investment cuts are instead bigger when employees have stronger bargaining power,

3A firm is classified to be in violation in any given year when the value of either its current ratio or its net worth fallsbelow the corresponding contractual threshold. We examine broader covenants in our robustness analysis (Table 6).

4Layoff announcement are collected from the Wall Street Journal and other major news sources using Factiva andLexis Nexis keyword searches.

5Our baseline results also pass several robustness checks, which include using a specification in changes, rather thanlevels; probit regression specifications of layoffs; alternative samples and definitions of covenant violations; and addingcontrol variables to address omitted variable concerns.

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which is consistent with firms substituting between their labor and capital margins of adjustment.

These results are robust across several firm- and industry-level proxies of agency problems and

labor bargaining.6 Variation by agency proxies suggests that the state-contingent allocation of con-

trol rights to creditors is effective as a mechanism to mitigate underlying "quiet life" type frictions,

which make managers reluctant to fire employees (see Bertrand and Mullainathan (2003), Cron-

qvist et al (2008), and Atanassov and Kim (2009) for evidence). Since labor rights drive a wedge

between the impact of creditor rights on employment vs. investment, there is an interplay be-

tween creditor and labor rights. Overall, variation by labor bargaining power suggests that there

is a "rivalry effect" between creditor and labor rights which is broadly consistent with the nexus

of contracts perspective of Jensen and Meckling (1976).

The impact of violations on employment is outsized in bad times and relatively muted in good

times, a finding that is robust across different proxies based on industry and macroeconomic ac-

tivity.7 For example, violations lead to employee cuts of about 29% in NBER recession years, and

their impact was truly outsized at about 42% in the Great Recession of 2008 and 2009. There

is even stronger evidence of time-series variation in the employment impact among firms with

weaker labor bargaining power and among non-rated firms, which likely have less access to al-

ternative sources of credit. The combination of a higher likelihood of violations and bigger job

cuts when violations occur leads to an estimated expected impact on employment which is about

5 times larger in recession than in non-recession times, which is consistent with a fundamental

tenet of much macroeconomics and finance that financing frictions exacerbate the real impact of

downturns. Since employment cuts are concentrated in exactly those times when creditors have

arguably the most bargaining power and labor has the least, time-series evidence further corrob-

orates our interpretation that the impact of violations reflects the relative strength of creditor and

6The firm-level proxies of agengy and financing frictions include: cash holdings, Gompers, Ishii, and Metrick (2003)GIM-Index, book leverage, and the fraction of total debt with short maturity, as well as a dummy for rated status. Theindustry-level labor bargaining proxies include: degree of union representation, labor intensity and flexibility, domesticand foreign product market competition.

7We thank Michael Roberts for suggesting these tests of time-series variation.

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labor rights.

Our evidence so far suggests that the ability of creditors to exercise their control rights is lim-

ited by labor rights. In our final set of tests, we ask whether loan terms impound labor rights and

price in a premium for creditors’ expected loss of effective control when labor is stronger. Our

identification is a regression discontinuity design that exploits the requirement by U.S. labor laws

that in order to create a new labor bargaining unit an election is held in which workers vote by

majority rule for or against union representation. We match administrative data from the National

Labor Relations Board (NLRB) on all union elections that took place in the US between 1985 and

2010 with loan pricing information from Dealscan and accounting data from Compustat, which

results in a sample of 3,814 loans for 1,756 unique election events.

Union wins are reliably associated with higher spreads on loans originated within two years

from the election,8 and the effect of unionization is particularly large for low rated and non-rated

borrowers which have most scope for state contingent transfer of control rights to creditors. This

result continues to hold when we use a matched sample methodology and when we consider only

"close" elections to address potential concerns about anticipation of election outcomes and omitted

variables issues. This evidence suggests that creditors demand compensation when employees

have more bargaining power, further corroborating our interpretation that labor rights limit the

impact of creditor rights on employees. The analysis also contributes to the classical literature

on the economic effects of unions (e.g., DiNardo and Lee (2004), Lee and Mas (2012)), which has

traditionally abstracted from corporate control issues.

Overall, our analysis indicates that creditor rights increase employment risk. To the best of our

knowledge, this is the first direct evidence consistent with the important implication of Jensen and

Meckling (1976) that there are conflicts of interest between creditors and nonfinancial stakeholders

with priority claims in asmuch as credit contracts that mitigate conflicts between debtholders and

8For example, in the overall sample, the mean loan spread for unions wins is 189.7 basis points, which is about 20basis points higher than the mean loan spread for union losses. This 20 basis points differential is highly statisticallyand economically significant at about 10 percent of the (unconditional) sample mean of loan spreads.

5

shareholders have spillover effects on employees. We make two main additional contributions

to the literature. First, our findings contribute to the literature on the real effects of the state

contingent transfer of control rights (Chava and Roberts (2008), Roberts and Sufi (2009), and Nini,

Smith, and Sufi (2009; 2012)) by identifying a risk-shifting channel from creditors to employees.

Our results indicate that the state contingent allocation of control rights to creditors is effective

as a mechanism to mitigate labor-related "quiet life" type agency frictions, which make managers

reluctant to fire employees (see Bertrand and Mullainathan (2003), Cronqvist et al (2008), and

Atanassov and Kim (2009)). By highlighting the interplay between labor rights and creditor rights

and by exploring the link between labor bargaining rights and loan spreads, our results also fill the

gap in the small but fast growing recent literature on labor and finance, which has so far mostly

focused on capital structure decisions (e.g., Matsa (2010) and Agrawal and Matsa (2013)).

Second, we contribute to the literature on financing and employment by providing identifi-

cation of financing effects.9 Existing evidence is relatively scant, since the literature has mostly

focused on financing and investment, and its interpretation is complicated by identification is-

sues, since financing variables are likely correlated with future growth prospects and firm’s de-

mand for labor. In addition to establishing an endogeneity-free link between financing frictions

and employment, we also offer direct evidence that binding financial covenants are an important

amplification mechanism of economic downturns,10 which supports theories such as Bernanke

and Gertler (1989) where a deterioration of firm net worth amplifies the effect of economic down-

turns by exacerbating financing frictions. Our evidence highlights a specific channel for the credit

restriction, namely covenant violations, and indicates that what makes bad times really bad for

workers is that creditors are more likely to exercise their control rights at the same time when

9Previous research has focused on the effects of finance and investment (Fazzari, Hubbard, and Petersen (1988);Whited (1992)); the effect of finance on employment (Ofek (1993), Hanka (1998), Kaplan (1989), Muscarella and Vet-suypens (1990), Davis, Haltiwanger, Jarmin, Lerner, and Miranda (2008), and Benmelech, Bergman, and Seru (2011)).In addition, previous studies have documented real costs of bankruptcy, such as lost customers and employee relation-ships (Titman and Opler (1994)).

10The influence of corporate financing on macroeconomic and financial stability (e.g., Kyotaki and Moore (1997),Bernanke and Gertler (1989)) and, specifically, on employment fluctuations (Sharpe (1994)) is a classic topic in macro-economics and finance.

6

employees have weaker bargaining power. While there is recent evidence that bankruptcies en-

tail costs for workers (Graham et al (2013)), our evidence shows that the real effects of finance

on employment are operative well before bankruptcy, which can help to explain why economic

downturns lead to large job losses even when they do not trigger a large wave of bankruptcies, as

in the case of the Great Recession of 2008 and 2009.

2 Analysis of Loan Covenant Violations and Employment

If the transfer of control rights to creditors has adverse consequences for employees, then there

should be a negative effect of loan covenant violations on employment. In this section, we exam-

ine this hypothesis using the regression discontinuity design approach pioneered in this literature

by Chava and Roberts (2008). After formally testing for the impact of violations on employees, we

examine which factors are driving the impact and show that the impact of violations varies pre-

dictably in the cross-section and in the time-series, and is concentrated among firms with greater

agency problems, those with greater bargaining power of creditors relative to employees, and in

bad times when labor markets have less slack, which corroborates our interpretation of the base-

line estimates.

2.1 Data and Sample Selection

Our sample consists of all Compustat firms incorporated in the United States that have relevant

loan covenant information from Loan Pricing Corporation’s (LPC) Dealscan database for the pe-

riod 1994 to 2010 which, after applying standard data filters, results in a final set of 11,536 firm-year

observations for 2,265 unique firms.

Our loan information comes from a 2011 extract of Loan Pricing Corporation’s (LPC) Dealscan

database. The data consist of dollar-denominated private loans made by bank (e.g., commercial

and investment) and nonbank (e.g., insurance companies and pension funds) lenders to U.S. cor-

7

porations during the period 1981 to 2010. Our sample construction strategy follows closely Chava

and Roberts (2008) and Dichev and Skinner (2002). Thus, in this section we summarize the main

parts of our sample construction strategy, detail the few parts where it differs from these papers,

and refer to Chava and Roberts (2008) for further details. We start with the annual merged CRSP-

Compustat database, excluding financial firms (SIC codes 6000-6999). While Chava and Roberts

(2008) primarily use quarterly data, we use annual data because firms do not report employment

at the quarterly frequency. We acknowledge that this data limitation is likely to make our assess-

ment of when the covenant violation occurs more noisy, although Chava and Roberts document

that their results also hold with annual data. All variables are defined in Appendix A.

Data from Compustat are merged with loan information from Dealscan by matching company

names and loan origination dates from Dealscan to company names and corresponding active

dates in the CRSP historical header file. The basic unit of observation in Dealscan is a loan, also

referred to as a facility or a tranche. Loans are often grouped together into deals or packages. Most

of the loans used in this study are senior secured claims, features common to commercial loans.

Because information on covenants is limited prior to 1994, we focus our attention on the sample

of loans with start dates between 1994 and 2010. Additionally, we require that each loan contains

a covenant restricting the current ratio, or the net worth or tangible net worth (which we group

together as net worth loans) to lie above a certain threshold.11

Since covenants generally apply to all loans in a package, we define the time period over which

the firm is bound by the covenant as starting with the earliest loan start date in the package and

ending with the latest maturity date. In effect, we assume that the firm is bound by the covenant

for the longest possible life of all loans in the package. A firm is in violation of a covenant if the

value of its accounting variable breaches the covenant threshold - i.e., when either the current ra-

tio or the net worth falls below the corresponding threshold.12 We focus on net worth and current

11We also require the covenant’s corresponding accounting measure to be non-missing. We also manually recoversome missing covenant information by looking at the package notes provided by Dealscan (package_comments).

12While conceptually straightforward, the measurement of the covenant threshold, and consequently the covenant

8

ratio covenants for two reasons, as elaborated by Chava and Roberts (2008) and Dichev and Skin-

ner (2002). First, they appear relatively frequently in the Dealscan database.13 Second, and most

importantly, the accounting measures used for these two covenants are standardized and unam-

biguous. As the earlier papers documented, while other restrictions with debt or leverage may

often be used, definitions can vary across contracts where debt can refer to long-term, short-term,

secured, or other debt, making it difficult to define violations. In robustness analysis, we consider

the impact of broadening the set of covenants. Since our focus does not discriminate between the

two covenants, for the purpose of our regression analysis there is a violation if either of the two

covenants is breached in any given firm-year.

We use two different measures of employment. One is the number of employees from Com-

pustat. The second is a dummy variable which is equal to one for firm-years when there is either

one of the 3,129 layoff announcements involving Compustat firms in the press, which we hand-

collected from the Wall Street Journal and other major news sources obtained from Factiva and

Lexis-Nexis news searches, or a reduction in the number of employees from Compustat (see Ofek

(1993) for a similar variable). In addition to results reported for this basic layoff variable, we also

report results for a medium-sized layoff dummy which corresponds to labor cuts of more than

5 percent of the workforce (which are those larger than the sample median of the distribution of

job cuts), and a large-sized layoff dummy for cuts of more than 10 percent of the workforce (top

quartile of the distribution of job cuts).

Table 1 provides summary statistics for the incidence of loan covenant violations as well as

means and medians of our main dependent variable, employment, and standard firm and in-

dustry characteristics in the resulting sample of 11,536 firm-year observations for 2,265 unique

firms that are bound by either a current ratio or a net worth covenant during the period 1994 to

violation, poses several challenges, such as the possibility of multiple overlapping deals, and, importantly, the fact thatcovenant thresholds can change over the life of the contract. We deal with these measurement issues following Chavaand Roberts (2008) (see their Appendix B for details).

13Table I in Chava and Roberts (2008) shows that covenants restricting the current ratio or net worth are found in9,294 loans (6,386 packages) with a combined face value of over a trillion dollars.

9

2010. By way of comparison, we also report summary statistics of these variables for other non-

financial firms in Compustat. Appendix A provides sources and detailed definitions for each of

these variables. Overall, our sample is comparable to those used in previous studies (Chava and

Roberts (2008), Dichev and Skinner (2002)). As in these studies, our sample of Compustat firms

with available loan covenant information contains firms that are somewhat larger, both in terms

of assets and number of employees, and have higher cash flow, profits, and leverage relative to

other firms in Compustat. The frequency of firm-year observations that are classified to be in vi-

olation is 20%, which is in line with the 15% frequency reported in Table 3 of Chava and Roberts

(2008), considering that there is some time-aggregation due to the fact that our sample frequency

is annual while theirs is quarterly and our longer sample period includes the Great Recession.

An advantage of having a longer time-series than previous studies is that we can document some

stylized time-series features of violations. In particular, the frequency of violations is markedly

higher in NBER recession years, 27%, than in non-recession years, 18%.

2.2 Empirical Framework and Estimation Approach

Our empirical specification follows the approach of Chava and Roberts (2008) and exploits their

insight that the "tightness" of loan covenants - i.e., the distance between the covenant threshold

and the actual accounting measure - can be used to estimate the causal effect of financing. In

particular, we consider covenant violations as the treatment and non-violations as the control,

and adopt a regression discontinuity design approach. We can do so since the treatment effect

is a discontinuous function of the distance between the underlying accounting variable and the

covenant threshold. Specifically, our treatment variable, Bindit, is defined as a dummy which

equals one if zit − z0it < 0, where i and t index firm and year observations, zit is the observed

current ratio (or net worth), and z0it is the corresponding threshold specified by the covenant.

Our baseline empirical model is

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Empi,t = α+ β× Bindi,t−1 + γ× Xi,t−1 + ηi + λt + νi,t (1)

where Empi,t is (log) employment, Bindit−1 = 1 if zit−1 − z0it−1 < 0 and zero otherwise is the

covenant violation dummy, Xi,t−1 is a vector of control variables measured at the fiscal year-end

prior to the year in which employment is measured, ηi is a firm fixed effect, λt is a year fixed

effect, and νi,t is a random error term assumed to be correlated within firm and potentially het-

eroskedastic (Petersen (2006)). Controls include variables that have been previously employed in

the loan covenants literature, such as firm size, profitability, and operating performance, as well

as in employment regressions (Nickell (1984), Nickell and Wadhwani (1991)), such as total labor

costs. In robustness analysis, we include additional controls such as market-to-book asset ratio,

leverage, Altman’s Z-score, and discretionary accruals.

The parameter of interest is β, which represents the impact of a covenant violation on employ-

ment (i.e., the treatment effect). Because of the inclusion of a firm-specific effect, identification of

β comes only from within-firm time-series variation for those firms that experience a covenant vi-

olation. As noted in Chava and Roberts (2008), the nonlinear relation in equation (1) provides for

identification of the treatment effect under very mild conditions. In fact, in order for the treatment

effect β to not be identified, it must be the case that the unobserved component of employment

(νj,t) exhibits an identical discontinuity as that defined in equation (1), relating the violation sta-

tus to the underlying accounting variable. That is, even if νj,t is correlated with the difference,

zit−1 − z0it−1, our estimate of β is unbiased as long as νj,t does not exhibit precisely the same dis-

continuity as Bindit−1.

Because the discontinuity is the source of identifying information, we also include smooth

functions of the distance from the technical default boundary in our baseline specification.14 In-

14More precisely, Default Distance (CR) and Default Distance (NW) are defined as Default Distance (CR) = I(CurrentRatioit)×(Current Ratioit - Current Ratio0

it), Default Distance (NW) = I(Net Worthit)×(Net Worthit - NetWorth0it), where

I(Current Ratioit) and I(Net Worthit) are indicator variables equal to one if the firm-year observation is bound by acurrent ratio or net worth covenant, respectively. The Current Ratio0

it and Net Worth0it variables correspond to the

covenant thresholds.

11

cluding these variables helps to isolate the treatment effect to the point of discontinuity and ad-

dresses the concern that the distance to the covenant threshold may contain information about

future investment opportunities not captured by the other controls. In addition, we report esti-

mates of equation (1) using the subsample of firm-year observations that are close to the point of

discontinuity. We follow Chava and Roberts (2008) and formally define the “Discontinuity Sam-

ple” as comprising firm-year observations for which the absolute value of the relative distance

between the accounting variable and the corresponding covenant threshold is less than 0.20. This

restriction reduces sample size to 4,469 firm-year observations,which is about 40% of the overall

sample.

2.3 The Response of Employment to Covenant Violations: Baseline Results

Table 2 reports results of estimating equation (1) in the entire sample (Panel A) and in the dis-

continuity sample (Panel B), respectively. All the specifications include year and firm fixed effects,

except for Column 4 which refers to a specification in changes with year and industry fixed effects.

First, we replicate the results of Chava and Roberts (2008) on investment in our sample even with

the addition of several recent years of data (Column 0). In the next sections we will use investment

responses as a benchmark to assess alternative explanations for our results.

Moving to employment, covenant violations are associated with a sharp decline in employ-

ment of about 19% per year (Column 1). The economic magnitude of the job cuts is substantial, at

about three times the 6% median yearly employment drop in the entire sample. In the discontinu-

ity sample, violations lead to employment drops of roughly the same magnitude (Column 1, Panel

B). Nonparametric analysis of average percentage annual changes in the number of employees in

event time leading to and after the year when a violation occurs confirms that there is a sharp

break in average employment in the year of violation (t = 0) and in the one immediately after

(t = 1), which is of roughly the same magnitude as the regression estimates (Figure 1).15

15In the years prior to violation (t = −4,−1), employment changes are close to zero on average. Employment

12

Our estimates of the impact of violations on employment are robust to using alternative spec-

ifications. Column 2 addresses omitted variable concerns by incorporating standard control vari-

ables (firm size, total wages, cash flows, and ROA), and Column 3 adds smooth functions of

the distance from the default boundary to further isolate the discontinuity corresponding to the

covenant violation. In this full specification, covenant violations remain associated with a sharp

decline in employment, which is about 18% per year. Signs of the coefficient estimates are as

expected, and the inclusion of the controls has little effect on the estimated impact of violations.

Column 4 reports estimates from the first difference analog to the fixed effects specification in

equation (1), which examines the change in the number of employees for a given firm in a given

year as a function of covenant violations, after controlling for changes in the control variables.

Fixed effects and first differences estimators are both consistent under standard exogeneity as-

sumptions (Wooldridge (2002)), thus making the comparison of the two specifications useful to

assess whether our baseline equation is properly specified. The first difference specification yields

estimates that are similar to the specification with fixed effects.

Finally, Columns 5 to 7 address the concern that the results may be driven by frictional volun-

tary separations rather than the firm decision to fire employees. We report estimates from a probit

analog to the baseline OLS regression analysis, which examine the probability that layoffs occur

for a given firm in a given year as a function of covenant violations and the full set of controls.16

The impact on layoffs is both qualitatively and quantitatively in line with the results of the impact

on the number of employees. Violations lead on average to a 19% higher likelihood of layoff in

a given year (Column 5). The impact is nearly identical when we consider only more discrete

medium-sized layoff events involving more than 5% of the workforce (Column 6), suggesting that

frictional separations are unlikely to be driving our results. The coefficient estimate is smaller for

continues to shrink somewhat in the subsequent years (t = 2, 3), with the annual change in number of employeesremaining negative and below its pre-violation average at about -8% per year on average.

16Layoffs have been considered in previous papers on financing and employment (see, for example, Hanka (1998))and are a common focus in the empirical labor literature.

13

layoffs that involve more than 10% of the workforce but the impact remains economically large at

about 10%, which is on the same order of magnitude as the unconditional likelihood of occurrence

of such large layoffs in our sample (Column 7).

2.4 Cross-sectional Variation in the Employment Response: Evidence on Agency and

Labor Bargaining Power

Based on our motivating theory and direct evidence from management discussion of covenant

violations, we expect that there should be cross-sectional variation in the impact of violations on

employment. First, the impact of violations should be larger for firms with more severe agency

frictions, since covenants are designed to mitigate agency and financing problems and there is evi-

dence supporting the "quiet life" hypothesis that agency problems make managers more reluctant

to fire employees (see Bertrand and Mullainathan (2003), Cronqvist et al (2008), and Atanassov

and Kim (2009)). Second, the impact should also be larger whenever employees are in a relatively

weaker bargaining position with respect to creditors, since financial contracting theory suggests

that employment cuts are brought about by a strengthening of creditor rights relative to labor

rights. Next, we test these two hypotheses in turn.

Table 3 shows evidence of variation by several firm-level proxies of agency and financing fric-

tions. In each year of the sample period, we rank firms based on the empirical distribution of these

proxies, which include cash holdings (Column 1), Gompers, Ishii, and Metrick (2003) GIM-Index

of antitakeover provisions (Column 2), book leverage (Column 3), and the fraction of total debt

with short maturity (Column 4), as well as a dummy for rated vs. nonrated status (Column 5).

Free cash flows (Jensen (1986)) and protection from disciplinary takeovers (Manne (1965)) are well-

known to exacerbate agency problems. Leverage, especially when mostly short-term and costly

to refinance, and lack of credit ratings increase financial constraints risk, thus potentially exacer-

bating risk-shifting (Jensen and Meckling (1976)). An alternative interpretation is that firms with

14

high leverage, shorter debt maturities, and no credit ratings have less financial slack and fewer al-

ternative borrowing opportunities, which increases their existing lenders’ bargaining power and

ability to exert influence upon violation.

We estimate the specification of equation (1)with the full set of controls and splines (Column 3

of Table 2) separately for the two groups of firms in the bottom and top quartiles of the (year-prior)

distribution of each of the four continuous proxies in turn, and for rated vs. nonrated firms. We

report results for the entire sample in Panel A and for the discontinuity sample in Panel B. For both

samples and both outcome variables (number of employees and the layoff dummy), the negative

impact of violations on employment is concentrated among firms that have higher cash-to-asset

ratios and antitakeover protection, those that are highly leveraged and have more short maturity

debt, and those with no credit rating (Rows 2, 4, 8, and 10). We also replicate the results in Chava

and Roberts (2008) for investment across the different proxies (Rows 6 and 12). Overall, these

results suggest that the state-contingent allocation of control rights to creditors helps to mitigate

"quiet life" employment distortions, and especially so for firms whose creditors are in a stronger

bargaining position at the time of violation.

Table 4 examines variation by various industry-level proxies of employees’ bargaining power

(Columns 1 to 4) and product market competition (Columns 5 and 6).17 In each year of the sample

period, we rank firms based on the empirical distribution of these proxies, which include mea-

sures of union representation (Columns 1 and 2), labor intensity and flexibility (Columns 3 and 4),

and domestic and foreign product market competition (Columns 5 and 6). Organized representa-

tion through unions is well-recognized to increase labor bargaining power (Clark (1984), Hirsch

(2008)). High labor to capital ratios reflect technological differences across industries in their mix

of productive factors, but may also indicate greater labor overhang and weaker bargaining power.

Bargaining power is also effectively higher when labor flexibility is lower, reflecting (sunk) costs of

17Using industry-level variables reduces the potential for simultaneity and for the case of labor intensity and flexibil-ity is motivated by the intuition that, due to technological differences, the extent to which firms face different costs ofadjusting labor varies across industries.

15

adjusting labor, which include hiring, training, and firing costs due to, for example, loss of human

and organizational capital as well as firm-specific employees skills (Oi (1962), Hamermesh (1989),

Eisfeldt and Papanikolaou (2011)). There is a classical theory literature and recent evidence that

product market competition mitigates agency frictions (Hart (1983), Giroud and Mueller (2011)).

Thus, we expect that the impact of violations on employment should be strongest for firms in

industries with higher domestic product market concentration and lower import penetration.

We estimate the full specification with controls and splines (Column 3 of Table 2) of equa-

tion (1) separately for the two groups of firms in the bottom and top quartiles of the (year-prior)

distribution of each of the industry-level proxies in turn, and report results for the entire sample

in Panel A and for the discontinuity sample in Panel B. The employment impact of violations is

concentrated among those firms that are in industries with lower union representation, higher la-

bor intensity and flexibility, and those in less competitive industries (Rows 1-4, and 7-10). These

results are robust for both samples and both outcomes variables (number of employees and the

layoff dummy). By contrast, the impact of violations on investment is less negative in industries

with lower union representation and those with higher labor intensity and flexibility (Rows 5-6,

and 11-12). Thus, labor bargaining power drives a wedge between employment and investment

responses, since the impact of violations on employment is smaller while the impact on invest-

ment is larger when labor has more bargaining power.

Overall, the cross-sectional variation by firm-level agency proxies suggests that the state con-

tingent allocation of control rights to creditors is effective as a mechanism to mitigate underlying

"quiet life" type frictions, which make managers reluctant to fire employees (see Bertrand and

Mullainathan (2003), Cronqvist et al (2008), and Atanassov and Kim (2009) for evidence). Varia-

tion by labor bargaining suggests that there is an important interplay between creditor and labor

rights, and that this interplay matters to understand how stronger creditor rights impact not only

employment, but also investment. Labor rights drive a wedge between the impact of creditor

16

rights on employment vs. investment, suggesting that there is a "rivalry effect" between creditor

and labor rights which is broadly consistent with the nexus of contracts perspective of Jensen and

Meckling (1976). Our finding of differential variation between investment and employment also

offers an additional test of our identification strategy. Mechanical explanations of our employment

effect as being simply driven by declining assets would predict that employment cuts should be

concentrated among the same set of firms that cut investment, which counters the evidence.

2.5 Time-series Variation in the Employment Response: Evidence on Industry and

Business Cycle Conditions

The influence of corporate financing on macroeconomic and financial stability (e.g., Kyotaki and

Moore (1997), Bernanke and Gertler (1989)) and, specifically, on employment fluctuations (Ofek

(1993), Sharpe (1994), Hanka (1998), and Davis, Haltiwanger, Jarmin, Lerner, and Miranda (2008))

is a classic topic in macroeconomics and finance. The recent financial crisis and the "great reces-

sion" in 2008 and 2009 with unemployment rates that peaked at 10 percent and 41 consecutive

months of rates above 8 percent have revived the academic and policy interest in understanding

the impact of financial frictions in the propagation of the business cycle shocks to employment.

However, interpretation of existing evidence based on the relation between measures of financ-

ing such as leverage ratios or cash flows and employment is complicated by identification issues,

since financing variables are likely correlated with future growth prospects and firm’s demand

for labor. Thus, we still do not have endogeneity-free evidence on whether financing frictions

exacerbate the impact of downturns on employees. In addition, since labor markets have less

slack in bad times, by exploiting time-series variation in employee bargaining power we can test

whether the employment impact of violations is concentrated in bad times, when employees have

less bargaining power and fewer outside job opportunities.

Table 5 reports results of this time-series tests, where we examine variation by various proxies

17

of bad times (Columns 1 to 3) vs. good times (Columns 4 to 6). For each year of the sample period,

we group firms into two bins based on whether or not (denoted by "Yes" or "No") in that year there

is an industry downturn (Column 1), a recession based on the NBER dates (Column 2), the "great

recession" (Column 3), an industry expansion (Column 4), the high-tech boom (Column 5), and

the "great moderation" (Column 6). We estimate the full specification18 of equation (1) separately

for the two bins and report results for the entire sample in Panel A.19

The employment impact of violations is outsized in bad times and relatively muted in good

times (Rows 1 and 3), a result that is robust across the different proxies of good and bad times and

our two main outcomes variables (number of employees and the layoff dummy). For example,

estimated responses imply that violations lead to employee cuts of about 29% in NBER recession

years (Column 2, Row 1), and to even bigger cuts of about 42% in the Great Recession (Column

3, Row 1). Evidence of time-series variation in the investment impact is weaker. For example, the

investment response in NBER recession periods is -0.9% (Column 2), which is about the same as

the average investment impact in Table 2. The relatively less pronounced time-series variation in

the investment impact with respect to the employment one is consistent with time-series variation

in employees’ bargaining power being an important driver of the employment response.

In Panel B we report results of the same set of tests when we further stratify the sample based

on firm and industry characteristics that were used in the analysis of Tables 3-4 and the number

of employees is the outcome. The firm-level characteristic we consider is firm credit rating sta-

tus (Rows 7 and 8). There is solid evidence that firms that have access to bond markets tend to

substitute bonds for loans in bad times (Kashyap, Stein, and Wilcox (1993), Ivashina and Becker

(2011)). Based on this evidence as well as our results in Table 3, we expect the time-series effects

to be concentrated among nonrated firms, which have less access to public debt markets. We also

present results for one of our industry-level proxies for union representation, union membership

18With the full set of controls and splines (Column 3 of Table 2).19Results for the discontinuity sample are qualitatively similar to those in Panel A and are omitted for brevity.

18

(Rows 9 and 10). Indeed, time-series variation in the employment impact is more pronounced for

firms that do not have a credit rating (Row 7) and for those in industries with lower union mem-

bership (Row 9), which suggests that the interplay between creditors and labor bargaining power

is an important factor behind the propagation effect of violations in downturns.

2.5.1 The employment response in recessions: a calibration

Theory suggests that financial contracting may exacerbate the effect of economic downturns on

employment and our analysis in Table 5 offers direct evidence in support of this notion. But how

large is the overall amplification effect of loan covenants? In order to facilitate a quantitative as-

sessment of the economic magnitude of the employment impact of violations in bad times, we

provide a simple calibration of the additional job cuts in recessions associated with a covenant

violation. There are two related but distinct sources of amplification. First, as shown in Table 1,

covenant violations are more frequent in bad times as measured by NBER recession years. Sec-

ond, our estimates in Table 5 imply that employee cuts are bigger in response to any given vio-

lation. Again, based on the NBER definition, in non-recession periods violation leads to 8.9% cut

in employees (Column 2, Row 2 of Table 5) and the frequency of bind is 18 percent (Table 1); in

recessions, violation leads to 29% cut (Column 2, Row 1 of Table 5) and the frequency of bind is 27

percent. Putting these effects together, the implied expected impact of covenant violations on em-

ployment in recession times is given by -0.078=0.27×-0.29, which is about 5 times larger than the

impact in non-recession periods, -0.016=0.18×-0.089. A similar calculation for investment sug-

gests that there is also amplification, but much less than for employment: violations lead to an

expected cut in investment in non-recession times of 0.001=0.006×0.18, vs. a cut in a recession of

0.0024=0.009×0.27, which is only twice as large. Thus, the interplay of labor and creditor rights

leads to larger amplification effects of violations on employment than on investment.

19

2.6 Robustness

In Table 6 we examine the robustness of the employment impact of violations to four batteries of

tests, which comprise using alternative specifications to address outliers and timing issues (Panel

A), using alternative samples and definitions of covenant violations to address alternative expla-

nations and potential measurement error issues (Panel B), and including additional control vari-

ables to address potential omitted variables concerns (Panels C and D). In all the tests, we take

the full specification20 of equation (1) as our starting point and report results for both the entire

sample (Columns 1 and 3) and the discontinuity sample (Columns 2 and 4). Starting with Panel

A, estimates from a median (quantile) regression specification are somewhat larger than OLS es-

timates (Row [1]), suggesting that outliers are unlikely to be driving our results. Adding a lagged

dependent variable (Row [2]),21 one more lag and two leads of Bind (Rows [3] and [4]) also leaves

the estimated impact little changed, suggesting that sluggish employment dynamics and related

timing issues are also not driving the results.

Moving to Panel B, estimates derived using an alternative definition of Bind based on the vio-

lation dummies hand-collected from SEC filings by Nini, Smith, and Sufi (2012), which are shown

in Row [5], remain large and are of the same order of magnitude as our baseline estimates, suggest-

ing that potential measurement error from not using actual violations is not an important concern.

A broader definition of Bind that includes the full set of covenants with threshold information

available in Dealscan (Row [6]) also leads to strongly statistically and economically significant

estimates, though notably lower than our baseline, consistent with the reasoning in Chava and

Roberts (2008) that net worth and current ratio covenants have most bite and are defined most

unambiguously, thus giving rise to the least potential attenuation bias from measurement error.

Excluding firm-years when there is a divestiture of assets (Row [7]) or the financial crisis (Row [8])

20With the full set of controls and splines (Column 3 of Table 2).21We are aware of the issue that OLS estimates may be biased in small-T unbalanced panels with firm fixed effects

and a lagged dependent variable. In additional robustness tests we have experimented with an IV-GMM estimationapproach (Bond and Van Reenen (2007)), which yields similar coefficient estimates for the emplyment impact of viola-tions.

20

has also little impact on our main estimates, which does not support alternative mechanical expla-

nations based on indirect effects from simply shrinking firms or one-time financial circumstances.

Panels C and D verify that our results are robust to controlling for several additional factors that

might affect employment,22 suggesting that omitted variables are not likely to be an important

concern.

2.7 Summary of Results

In sum, the results so far show that covenant violations and the associated transfer of control

rights to creditors lead to sizable employment cuts. In the cross-section, the employment cuts

are concentrated among firms with more severe agency and financing frictions, as well as those

whose creditors have more bargaining power and whose employees have less bargaining power,

suggesting that the state contingent allocation of creditor control rights is an effective mechanism

to mitigate underlying "quiet life" type agency frictions. In addition, our evidence suggests that

there is an interplay between creditors and labor rights, since labor rights affect the overall effec-

tiveness of the transfer of control rights to creditors, which is broadly consistent with the nexus of

contracts perspective of Jensen and Meckling (1976).

The evidence of differential variation of the employment and the investment impact by labor

power corroborates our interpretation that violations have a direct effect on employees because

they lead to a transfer of control rights to creditors. A mechanical explanation of the effect of vio-

lations would predict cuts in both employment and investment which would not vary with labor

bargaining power. Finally, our results on time-series variation of the employment impact of vio-

lations further corroborates our interpretation that the fundamental rivalry between creditor and

labor rights is driving our results, since employment cuts are concentrated in exactly those times

when creditors have the most and labor has the least bargaining power. The time-series analysis22In particular, we include investment (Row [9]); a dummy for whether the firm undergoes a divestiture of assets

in any given year (Row [10]); 2nd- and 5th-order non-liner splines of the distance from the covenant threshold (Rows[11] and [12]); book leverage (Row [13]); Tobin’s Q (Row [14]); Altman’s Z-score (Row [15]); and discretionary accruals(Row [16]). The estimated impact of covenant violations on employment is stable across all these different controls.

21

also offers the first endogeneity-free evidence that, consistent with a fundamental tenet of much

macroeconomics and finance literature, financing frictions exacerbate the impact of downturns on

employees.

3 Analysis of Union Elections and Loan Pricing

Our main evidence so far is that covenant violations lead to substantial employment cuts, but

less so when labor has bargaining power, which suggests that labor rights limit creditors’ control

rights. In this section’s additional analysis of loan pricing terms, we ask whether creditors antic-

ipate that labor rights may limit their control rights upon violation of a covenant. If this is the

case, then we expect that loan terms should impound the strength of labor bargaining rights and

price in a premium for creditors’ expected reduced effective control. These tests offer subsidiary

evidence of an interplay between labor rights and creditor rights, which further corroborates our

interpretation of the employment impact of violations. The analysis also contributes to the clas-

sical literature on the economic effects of unions (e.g., DiNardo and Lee (2004)), which has tra-

ditionally abstracted from corporate control issues and focused on the impact of unions on labor

market outcomes, such as wages (see Lee and Mas (2012) for a recent study on unions and equity

prices).

While there is solid evidence that unionized workers have stronger bargaining rights (Clark

(1984), Hirsch (2008)),23 empirical tests based on labor union representation face a classical en-

dogeneity challenge: cross-sectional comparison of loan pricing between unionized and non-

unionized firms is complicated by potential omitted variable bias if the two groups of firms differ

along other characteristics that may affect loan prices. To overcome this challenge, we assemble

a new dataset that combines information on elections to establish union representation with loan

and firm information from Dealscan and Compustat. Our main identification is a regression dis-

23Which include bargaining over wages, pensions, and a variatey of work-related issues with the employer.

22

continuity design that exploits the requirement by US labor laws that in order to create a new labor

bargaining unit, an election is held in which workers vote for or against union representation and

a simple majority rule is followed to determine whether or not they become unionized. We look

at yield spreads of loans issued in the two years following elections and ask whether there is a

significant spread differential depending on whether the result is a win or a loss for unions. Re-

sults within a close range around the 50 percent majority threshold are our "discontinuity sample,"

within which election outcomes are plausibly a "quasi-random" experiment. We also complement

these local estimates with a matched-sample analysis for the overall sample.

In the remainder of this section, after describing our sample selection and construction criteria,

we summarize the results on the impact of unionization on loan pricing.

3.1 Data

We match administrative data from the National Labor Relations Board (NLRB) on all union elec-

tions that took place in the US between 1985 and 2010 with loan data from our 2011 extract of

Dealscan for firms that have balance sheet variables available in Compustat.24 This is a labor

intensive task since it involves matching company names and union election dates for a very

large number of events from NLRB to company names and corresponding active dates in the

CRSP-Compustat historical header file. Since the bulk of our sample construction strategy follows

closely the literature on the economic impact of unionization events (DiNardo and Lee (2004), and

especially Lee and Mas (2012), whose Data Appendix we refer to for details), we only highlight

our main innovations.

Availability of loan pricing information from Dealscan restricts our usable NLRB data with

respect to previous studies, which generally rely on a longer time series (1961-) and the entire

Compustat universe. Due to this constraint and in order to insure that our hypothesis testing

24Since we are not using loan covenant information for this part of the analysis, we are not constrained by covenantdata availability and, hence, we can use the entire Dealscan sample.

23

has enough power even for the "discontinuity sample" defined within a narrow band around the

50 percent majority threshold, we take several steps to increase the sample size. The main step

involves implementing a second-pass name match for NLRB firms that were not matched in the

CRSP-Compustat historical header file, for which we used: (i) a list of historical company names

retrieved from Capital IQ; and (ii) a list of historical links between CRSP-Compustat firms and the

company names of their operating segments and subsidiaries also from Capital IQ.

Summary statistics for the final sample of 3,814 loan observations for 1,756 unique election

events that have information on the percentage vote for unionization during the period 1985 to

2010 are tabulated in Table 7. Panel A reports means (and medians) for union election variables: a

union win dummy, which is equal to one for any given election that results in a win for the union,

and two important election characteristics, size, which is the number of employees involved, and

percentage share of votes that were cast in favor of unionization. Overall, these statistics are

broadly in line with those in previous studies (e.g., Lee and Mas (2012)), indicating that loan infor-

mation availability from Dealscan does not lead to issues with selection from the NLRB universe.

Firms in our sample are larger, more likely to be highly rated, and have somewhat lower spreads

than other firms in Dealscan-Compustat, another feature we share with previous studies.

Finally, a simple diagnostic comparison of pre-event firm characteristics and loan spreads be-

tween firms where elections resulted in a win and those that resulted in a loss for the union is

tabulated in Panel B for the overall sample, and in Panel C for the "discontinuity sample" of "close"

elections, defined as a narrow range (a vote share range of±5%) around the majority (50%) thresh-

old needed for the union to win representation. While there are some residual differences in the

overall sample, especially in terms of prior spreads, these differences go away in the discontinuity

sample, which validates our key identifying assumption.

24

3.2 The Impact of Unionization on Loan Spreads: Results

Table 8 reports results of simple t-tests of differences between mean loan spreads in the first and

in the second year after union elections (Columns (1) to (4) and Columns (5) to (8), respectively)

depending on whether the election resulted in a win or a loss for the union. In Panel A, we report

results for the entire sample (Columns (1), (5)) and for various sub-samples that exclude elections

involving, in turn, operating subsidiaries (Columns (2), (6)), fewer than 150 employees (Columns

(3), (7)), and those involving both fewer than 150 employees and investment grade-rated firms

(Columns (4), (8)).

Union wins are associated with significantly higher loan spreads, a result which is robust to

the different sub-samples and both time windows. In the overall sample, the mean loan spread

for borrowers where unions win the election is 189.7 basis points, which is about 20 basis points

higher than the mean loan spread for borrowers where unions lose (Column 1). This spread dif-

ferential is not only statistically significant, but also economically significant at about 10 percent of

the sample mean loan spread. The differential triples in magnitude when we consider relatively

larger elections involving low rated and nonrated borrowers and it about doubles for loans issued

two years after the election. Combined, these results suggest that the effect of unionization on

loan spreads is long lasting and is concentrated among the firms that have most scope for state

contingent transfer of control rights to creditors.25

In Panel B, we repeat these t-tests of differences but now sharpen our identification by exploit-

ing the unique feature of the NLRB data that we can observe the percentage vote for unionization

in any given election. We use the percentage vote variable to restrict the sample and include only

"close" elections, which are defined as a narrow range (a vote share range of ±5%) around the

majority (50%) threshold needed for the union to win representation ("Discontinuity sample").26

25Using equity prices, Lee and Mas (2012) also find long lasting effects of unionization events.26This regression discontinuity design is standard in the literature and relies on plausibly exogenous "local" variation

in unionization around the 50% threshold, which is due to the fact that unions cannot control the assignment variable(votes) near the threshold.

25

The impact of unionization on loan spreads is larger than in the overall sample, with a premium

for union wins now ranging between about 70 and 150 basis points. Graphical analysis in Figure

2, which plots mean loan spreads for each of ten bins of the data sorted on deciles of the union

vote share variable, offer additional nonparametric evidence that there is a sharp break in average

loan spreads around the 50% threshold.

Finally, Panel C shows that, when we further stratify the sample based on the number of em-

ployees involved in each election, the loan spread differential between union wins and losses

increases monotonically with the size of the election. Since larger elections extend the reach of la-

bor rights, they likely impose greater limitations on the state contingent transfer of control rights

to creditors. Stronger results for the "discontinuity sample" and for larger elections suggest that

anticipation of the election outcomes and other potential omitted variable issues lead, if anything,

to downward biased estimates of the effect of unionization. Thus, the impact of unionization of

loan spreads is unlikely to be an artifact of endogeneity issues.

3.2.1 Matched-Sample Analysis and Additional Robustness

In our last set of tests, we use a matched sample methodology analogous to long-run event-

studies (e.g., Barber and Lyons (1997)) and construct a "benchmark" spread for a portfolio of loans

matched on year, industry, and a variety of firm and loan characteristics. We use this approach

to check whether the baseline results in Panel A of Table 8 are robust to controlling for common

shocks occurring by chance that affect firms with similar characteristics. Results are reported in

Table 9, which shows t-tests for the means of excess loan spreads in the two years after union elec-

tions, which are defined as the difference between loan spreads and the average loan spread for a

portfolio of loans matched based on year, industry, and, in turn, (deciles of) firm size in Columns

(1) to (4) of Panel A; growth opportunities (Market to book ratio) in Columns (5) to (8) of Panel B;

credit ratings in Columns (1) to (4) of Panel C; and year-prior loan spreads in Columns (5) to (8)

26

of Panel D. Robustly across these four benchmarks, union wins remain reliably associated with

higher loan spreads. The differential in excess spreads between unions wins and union losses re-

mains economically significant. For example, in the overall sample, the mean loan spread in excess

of the benchmark based on year-prior spread is about 17 basis points, which is still about 10 per-

cent of the sample mean loan spread (Panel D, Column 5). The spread differential is again much

higher and ranging between about 60 and 90 basis points for relatively larger elections involv-

ing high-yield and nonrated borrowers. Thus, controlling for common shocks leaves our baseline

results little changed.

We implemented a battery of additional robustness tests, which are not tabulated to conserve

space.27 In particular, we confirmed that the results in Table 8 are robust to the following: (i)

addressing potential outliers by either repeating the t-test analysis on the logarithm of spreads or

by using Mann-Whitney (z-statistic) tests; (ii) estimating a full-fledged polynomial regression of

loan spreads on union win dummy, while controlling for smooth and higher order polynomials

of the union vote share as well as standard firm and loan characteristics, and year and industry

fixed effects. An additional advantage of this robustness check is that we have verified that the

coefficient of the union win dummy remains statistically significant when we cluster standard

errors at the firm level, which addresses the potential concern that multiple election events for the

same borrower firm-year may affect our assessment of statistical significance in Table 8;28 (iii) a

series of placebo or falsification tests in which we take arbitrary thresholds for the union share

vote and an associated "discontinuity" band and examine if unionization around these artificial

thresholds is related to borrowers’ post-election loan spreads. We found no statistical significance

around the two placebo thresholds we considered (40% and 60%), suggesting that our baseline

results are not spurious.

Overall, the analysis in this section indicates that union wins in elections to set up new la-

27Tabulations of the results are available upon request.28We have also verified that the results are robust to retaining the outcome of the largest election only in the cases

when there are multiple elections for any given firm-year.

27

bor bargaining units are associated with higher loans spreads, and especially so for firms that are

rated below investment grade where creditors have more scope for mitigating risk-shifting issues

through the state contingent transfer of control rights. This evidence suggests that creditors de-

mand compensation when employees gain bargaining power. This evidence further corroborates

our interpretation that there is a transfer of control rights to creditors in response to covenant

violations and stronger labor rights mitigate the impact of creditor rights on employees.

4 Conclusion

Stronger creditor rights increase employment risk. We have provided robust evidence that loan

covenant violations and the associated transfer of control rights to creditors have significant ad-

verse effects on employment. In response to a loan covenant violation, employment drops by

about 18% per year, with even deeper cuts for firms with more severe agency problems, those

whose employees have relatively weaker bargaining power, and in times when industry and

macroeconomic conditions are weak. Labor rights not only mitigate the employment impact

of creditor rights, but also affect creditors’ loan pricing decisions. Ours is the first direct evi-

dence that even away from bankruptcy states there are conflicts of interest between creditors and

other stakeholders with priority claims. Thus, our evidence suggests that credit contracts between

debtholders and shareholders have spillover effects on nonfinancial stakeholders. In addition, our

evidence shows that there are real effects of financial contracting on employment and that these

effects are operative before debt default or bankruptcy, which we have argued can contribute to

explain why economic downturns lead to large job losses even when they do not trigger a large

wave of bankruptcies, as in the case of the Great Recession of 2008 and 2009.

28

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31

Appendix A: Variable Definitions

The variables used in this paper are extracted from four major data sources: Loan Pricing Cor-poration’s (LPC) Dealscan database, COMPUSTAT, CRSP, and the National Labor Relations Board(NLRB). For each data item, we indicate the relevant source in square brackets. The variables aredefined as follows:

Loan Covenants [Dealscan]:Bind is a dummy that takes value of one if either net worth or current ratio fall below their respec-tive loan covenant thresholds in any given firm-year.NW is the net worth covenant threshold.CR is the current ratio covenant threshold.

Outcome Measures:Log(Employment) is the natural logarithm of the total number of employees (item 29). [Compustat]Layoff (All) is a dummy that takes value of one if there is a decline in employment in any given yearfrom the previous year. We complement Compustat data with information on 3,129 hand-collectedlayoff announcements from Wall Street Journal and other major news sources [Compustat, Factivaand Lexis Nexis news searches].Layoff (Medium) is a dummy that takes value of one if there is a larger than average (5%) declinein employment in any given year from the previous year. We complement Compustat data withinformation on 3,129 hand-collected layoff announcements from Wall Street Journal and othermajor news sources [Compustat, Factiva and Lexis Nexis news searches].Layoff (Big) is a dummy that takes value of one if there is a larger than 10% decline in employmentin any given year from the previous year. We complement Compustat data with information on3,129 hand-collected layoff announcements from Wall Street Journal and other major news sources[Compustat, Factiva and Lexis Nexis news searches].Investment is capital expenditures (item 128) over net property, plant and equipment at the begin-ning of the fiscal year (item 8). [Compustat]Loan spread is the all in spread on loans, including fees [Dealscan].

Union Elections [NLRB]:Union Win is a dummy that takes value of one for any given election that results in a win for theunion.Union Election Size is the number of employees that are eligible to vote in any given election.Union Vote Share is the percentage of votes cast in favor of the union in any given election.

Firm and Industry Variables:

Baseline Controls:Log(Assets) is the natural logarithm of the book value of assets (item 6), deflated by CPI in 1990.[Compustat]Total Wages is the natural logarithm of total labor expenses (item 42), deflated by CPI in 1990.[Compustat]Cash Flow is the ratio of income before extraordinary items plus depreciation and amortizationover the ratio of net property, plant and equipment at the beginning of the fiscal year to totalassets. [Compustat]Return on assets (ROA) is the ratio of operating income after depreciation (item 178) over laggedtotal assets (item 6). [Compustat]Default Distance (NW) is the difference between the net worth covenant threshold and total assetsminus total liabilities. [Compustat]

32

Default Distance (CR) is the difference between the current ration covenant threshold and the ratioof current assets to current liabilities. [Compustat]

Sample-Split Variables:Cash Holdings is the ratio of cash holdings (item 1) to total assets (item 6). [Compustat]GIM Index is the index of antitakeover provisions by Gompers, Ishii, and Metrick (2003).Leverage is long term debt (item 9) plus debt in current liabilities (item 34) over the sum of longterm debt (item 9) plus debt in current liabilities (item 34) plus market value of equity (item25*item199). [Compustat]Short Term Debt is the fraction of a firm’s total debt that matures in three years or less. [Compustat]Rating is a dummy variable that takes the value of one if the firm has an S&P Long-Term DomesticIssuer Credit Rating [Compustat]Industry Unionization is the share of employees in any given industry-year that are members of aunion (Membership) or covered by a collective bargaining agreement (Coverage).Industry Labor Intensity & Labor Adjustment Costs are measured as the average ratio of number ofemployees to total assets (Labor-Capital Ratio) and the average ratio of capitalized selling, general,and administrative (SG&A) expenses to total assets (Adjustment Costs) [Compustat]Industry Product Market Competition is measured by the Herfindahl-Hirschman Index (HHI) andthe share of imports to the total value of shipments (Import Penetration) [Compustat]Bad Times are measured as industry-years in the bottom quartile of sales growth (Industry Down-turn), a dummy that takes value of one in NBER recession years (NBER Recession), and a dummythat takes value of one in 2008 and 2009 (The Great Recession) [Compustat & NBER]Good Times are measured as industry-years in the top quartile of sales growth (Industry Expansion),and a dummy that takes value of one for firms in the semiconductors, computer manufacturing,and telecommunications sectors for the 1993-2000 period (High Tech Boom) and a dummy that takesvalue of one in the 1993-2000 period (The Great Moderation) [Compustat & NBER]

Additional Controls:Tobin’s Q (M/B) is the market value of assets divided by the book value of assets (item 6), wherethe market value of assets equals the book value of assets plus the market value of common equityless the sum of the book value of common equity (item 60) and balance sheet deferred taxes (item74). [Compustat]R&D is the ratio of R&D expenditures (item 46, or 0 is missing) over lagged sales (item 12). [Com-pustat]Advertising is the ratio of advertising expenditures (item 45, or 0 if missing) over lagged total sales(item 12). [Compustat]Free Cashflow is the ratio to total assets (item 6) of operating income before depreciation (item 13)less interest expense (item 15) and income taxes (item 16) and capital expenditures (item 128).[Compustat]Altman’s Z-Score is the sum of 3.3 times pre-tax income, sales, 1.4 times retained earnings, and 1.2times net working capital all divided by total assets. [Compustat]Accruals TWW and Accruals DD are as defined in Chava and Roberts (2008). [Compustat]

33

Table 1: Loan Covenant Sample: Summary Statistics

This table presents summary statistics (means and medians) for our merged Dealscan-Compustat sample,which consists of 11,536 firm-year observations for nonfinancial firms between 1994 and 2010 correspond-ing to firms that have at least one private loan found in Dealscan with a covenant that restricts current ratioor net worth to lie above a certain threshold (Columns 1 and 2). For the sake of comparison, Columns 3and 4 report summary statistics (means and medians) for the Other Compustat sample, which consists of110,058 firm-year observations for nonfinancial firms in the same period that have no matching informationin Dealscan. Definitions for all variables are in Appendix A.

Dealscan-Compustat Other CompustatMean Median Mean Median

(1) (2) (3) (4)Loan Covenant Violations:Bind 0.20 0 n.a. n.a.

Excluding NBER Recession Years 0.18 0 n.a. n.a.Only in NBER Recession Years 0.27 0 n.a. n.a.

Employment Outcome Variables:Employees (000) 7.75 2.16 7.45 0.75Layoff Dummy:

All 0.38 0 0.38 0Medium 0.22 0 0.20 0Large 0.09 0 0.10 0

Capex 0.07 0.04 0.07 0.04

Firm Characteristics:Assets (Log) 5.9 6.0 5.1 4.9Total Wages (Log) 4.7 4.5 4.3 4.5Cash Flow 0.08 0.08 0.04 0.08ROA 0.10 0.11 0.06 0.10Net Worth 476 149 471 43Tangible Net Worth 179.8 60.3 123.8 29.3Current Ratio 2.10 1.76 2.30 1.79Cash Holdings 0.10 0.05 0.20 0.10GIM Index 9.30 9.00 9.20 9.00Leverage 0.29 0.28 0.25 0.20Short Term Debt 0.13 0.05 0.12 0.05Rated Dummy 0.32 0 0.18 0Tobin’s Q 1.94 1.36 1.89 1.41

Industry Characteristics:Unionization 0.10 0.08 0.09 0.06Labor Intensity 0.01 0.01 0.01 0.01Competition (HHI) 0.23 0.18 0.22 0.17Competition (Import Penetration) 0.24 0.21 0.24 0.20

Firm-Year Obs 11,536 110,058Firms 2,265 15,186

34

Tabl

e2:

Loan

Cov

enan

tVio

lati

ons

and

Empl

oym

ent:

Base

line

Reg

ress

ion

Ana

lysi

s

This

tabl

epr

esen

tsre

gres

sion

resu

lts

ofem

ploy

men

ton

aco

vena

ntvi

olat

ion

mea

sure

("Bi

nd")

and

cont

rols

.Th

ede

pend

ent

vari

able

isth

era

tio

ofca

pita

lex

pend

itur

esto

asse

tsat

the

star

toft

hepe

riod

inC

olum

n(0

),to

ensu

reco

mpa

rabi

lity

ofsa

mpl

esto

Cha

vaan

dR

ober

ts(2

008)

;log

empl

oym

enti

nC

olum

ns(1

)to

(3),

empl

oym

ent

grow

th(t

hera

tio

ofnu

mbe

rof

empl

oyee

sto

lagg

ednu

mbe

rof

empl

oyee

s)in

Col

umn

(4),

and

adu

mm

yth

atta

kes

valu

eof

one

inan

ygi

ven

firm

-yea

rw

hen

ther

eis

ala

yoff

inC

olum

ns(5

)to

(7).

All

vari

able

defin

itio

nsar

ein

App

endi

xA

.All

inde

pend

ent

vari

able

s,ex

cept

cash

flow

,ar

ela

gged

one

year

.Pa

nelA

pres

ents

the

resu

lts

for

the

enti

resa

mpl

e.Pa

nelB

only

uses

firm

-yea

rob

serv

atio

nsin

whi

chfir

ms

are

clos

eto

viol

atin

gth

eco

vena

nt,d

efine

das

ana

rrow

rang

e(±

20%

)aro

und

the

cove

nant

thre

shol

d("

Dis

cont

inui

tysa

mpl

e").

Spec

ifica

tion

sin

Col

umns

(0)t

o(3

)inc

lude

both

firm

and

year

fixed

effe

cts,

whi

leC

olum

ns(4

)to

(7)

incl

ude

indu

stry

and

year

fixed

effe

cts.

Stan

dard

erro

rsro

bust

tohe

tero

sked

asti

city

and

wit

hin-

firm

seri

alco

rrel

atio

nap

pear

belo

wpo

inte

stim

ates

.Lev

els

ofsi

gnifi

canc

ear

ein

dica

ted

by*,

**,a

nd**

*fo

r10

%,5

%,a

nd1%

resp

ecti

vely

.

Pane

lA:E

ntir

eSa

mpl

eD

epen

dent

Var

iabl

e:In

vest

men

tlo

g(Em

ploy

men

t)Em

pG

row

thLa

yoff

s(0

)(1

)(2

)(3

)(4

)(5

)(6

)(7

)M

odel

Spec

ifica

tion

:FE

FEFE

FEC

ontr

ols

OLS

Con

trol

sPr

obit

Prob

itPr

obit

No

Con

trol

sN

oC

ontr

ols

Con

trol

s&

Splin

es&

Splin

esA

llM

ediu

mLa

rge

Bind

-0.0

10∗∗∗

-0.1

94∗∗∗

-0.1

74∗∗∗

-0.1

76∗∗∗

-0.1

58∗∗∗

0.18

8∗∗∗

0.19

2∗∗∗

0.10

9∗∗∗

(0.0

03)

(0.0

25)

(0.0

22)

(0.0

22)

(0.0

27)

(0.0

14)

(0.0

15)

(0.0

10)

Log(

Ass

ets)

0.26

1∗∗∗

0.25

8∗∗∗

0.13

6∗∗

-0.0

27∗∗∗

-0.0

26∗∗∗

-0.0

01(0

.024

)(0

.025

)(0

.058

)(0

.004

)(0

.004

)(0

.002

)To

talW

ages

0.04

20.

041

0.08

9-0

.002

-0.0

01-0

.001

(0.0

29)

(0.0

29)

(0.0

57)

(0.0

05)

(0.0

04)

(0.0

02)

Cas

hFl

ow0.

059

0.06

80.

065∗∗

-0.1

86∗∗∗

-0.0

86∗∗

-0.0

26∗

(0.1

15)

(0.1

15)

(0.0

32)

(0.0

48)

(0.0

33)

(0.0

16)

RO

A0.

418∗∗∗

0.41

5∗∗∗

0.14

5∗∗∗

-0.4

36∗∗∗

-0.4

11∗∗∗

-0.2

18∗∗∗

(0.1

22)

(0.1

22)

(0.0

35)

(0.0

74)

(0.0

59)

(0.0

32)

Def

ault

Dis

tanc

e(N

W)

0.00

1-0

.004

-0.0

010.

001

-0.0

00(0

.008

)(0

.005

)(0

.003

)(0

.002

)(0

.001

)D

efau

ltD

ista

nce

(CR

)-0

.019∗∗

0.03

40.

001

0.01

10.

002

(0.0

08)

(0.0

30)

(0.0

04)

(0.0

09)

(0.0

06)

Inte

rcep

t0.

088∗∗∗

0.33

1∗∗∗

-0.8

67∗∗∗

-0.8

46∗∗∗

0.21

8∗∗∗

(0.0

05)

(0.0

83)

(0.1

38)

(0.1

39)

(0.0

48)

Firm

Fixe

dEf

fect

sYe

sYe

sYe

sYe

sN

oN

oN

oN

oIn

dust

ryFi

xed

Effe

cts

No

No

No

No

Yes

Yes

Yes

Yes

Year

Fixe

dEf

fect

sYe

sYe

sYe

sYe

sYe

sYe

sYe

sYe

s

Obs

erva

tion

s11

,536

11,4

2611

,065

11,0

6510

,965

10,8

6510

,951

10,9

51

Pane

lB:D

isco

ntin

uity

Sam

ple

Bind

-0.0

08∗∗∗

-0.1

62∗∗∗

-0.1

40∗∗∗

-0.1

34∗∗∗

-0.1

61∗∗∗

0.15

2∗∗∗

0.11

1∗∗∗

0.07

0∗∗∗

(0.0

03)

(0.0

31)

(0.0

30)

(0.0

30)

(0.0

40)

(0.0

26)

(0.0

26)

(0.0

18)

Obs

erva

tion

s4,

469

4,40

34,

193

4,19

34,

179

4,05

54,

091

4,09

1

35

Table 3: Loan Covenant Violations and Employment: By Proxies of Agency and Financing

This table presents regression results of employment on a covenant violation measure ("Bind") and controls for differentsub-sample splits of the data based on ex-ante proxies for the severity of agency (Columns (1) and (2)) and financing(Columns (3) to (5)) frictions faced by firms. The model specification is the one with firm fixed effects, controls, andsplines as in Column (3) of Table 2 and the dependent variable is log employment in Rows [1]-[2] and [7]-[8], a dummythat takes value of one in any given firm-yearn when there is a layoff in Rows [3]-[4] and [9]-[10], and the ratio ofcapital expenditures to assets at the start of the period in Rows [5]-[6] and [11]-[12]. All variable definitions are inAppendix A. We only report estimates of the Bind coefficient and omit estimates of firm controls from the table forbrevity (available upon request). Panel A presents the results for the entire sample. Panel B only uses firm-year ob-servations in which firms are close to violating the covenant, defined as a narrow range (±20%) around the covenantthreshold ("Discontinuity sample"). These samples are split between bottom and top quartiles of (year-prior) values ofthe following ex-ante proxies of agency frictions: cash holdings (Column (1)), and Gompers, Ishii, and Metrick (2003)GIM index of antitakeover provisions (Column (2)); and between bottom and top quartiles of (year-prior) values of thefollowing ex-ante proxies of financing frictions leverage (Column (3)) and the fraction of total debt with short maturity(Column (4)), as well as credit rating status (Column (5)). Standard errors robust to heteroskedasticity and within-firmserial correlation appear below point estimates. Levels of significance are indicated by *, **, and *** for 10%, 5%, and1% respectively.

Panel A: Entire SampleAgency Financing

(1) (2) (3) (4) (5)Cash GIM Leverage Short Term Credit

Holdings Index Debt RatingLog(Employment)[1] Q1 -0.049 -0.065 -0.052 -0.086 Yes -0.095∗∗

(0.042) (0.076) (0.050) (0.068) (0.039)[2] Q4 -0.228∗∗∗ -0.303∗∗∗ -0.200∗∗∗ -0.243∗∗∗ No -0.185∗∗∗

(0.077) (0.072) (0.044) (0.079) (0.028)Layoffs, Probit[3] Q1 0.053∗∗∗ 0.023 0.058∗∗ 0.032 Yes 0.012

(0.017) (0.012) (0.030) (0.024) (0.012)[4] Q4 0.156∗∗∗ 0.128∗∗∗ 0.154∗∗∗ 0.187∗∗∗ No 0.112∗∗∗

(0.034) (0.060) (0.017) (0.028) (0.012)Investment[5] Q1 -0.003 -0.003 -0.002 -0.001 Yes -0.006

(0.006) (0.006) (0.007) (0.006) (0.004)[6] Q4 -0.020∗∗∗ -0.011∗∗ -0.013∗∗ -0.011∗∗ No -0.014∗∗∗

(0.006) (0.006) (0.006) (0.004) (0.003)Panel B: Discontinuity Sample

Log(Employment)[7] Q1 -0.035 -0.038 -0.037 -0.064 Yes -0.052

(0.058) (0.140) (0.078) (0.074) (0.054)[8] Q4 -0.233∗∗∗ -0.228∗∗∗ -0.217∗∗∗ -0.267∗∗ No -0.182∗∗∗

(0.078) (0.083) (0.067) (0.117) (0.036)Layoffs, Probit[9] Q1 0.041∗∗ 0.028 0.021 0.024 Yes 0.013

(0.021) (0.019) (0.028) (0.025) (0.024)[10] Q4 0.148∗∗∗ 0.178∗∗ 0.189∗∗∗ 0.196∗∗∗ No 0.124∗∗∗

(0.036) (0.116) (0.023) (0.035) (0.016)Investment[11] Q1 -0.002 -0.006 -0.002 -0.006 Yes -0.006

(0.005) (0.007) (0.008) (0.006) (0.004)[12] Q4 -0.019∗∗ -0.022∗∗ -0.014∗∗∗ -0.016∗∗ No -0.013∗∗∗

(0.008) (0.011) (0.006) (0.007) (0.004)

36

Table 4: Loan Covenant Violations and Employment: By Proxies of Labor Bargaining Power

This table presents regression results of employment on a covenant violation measure ("Bind") and controls for differentsub-sample splits of the data based on ex-ante proxies for industry unionization (Columns (1) and (2)), labor intensityand flexibility (Columns (3) and (4)) and product market competition (Columns (5) and (6)). The model specificationis the one with firm fixed effects, controls, and splines as in Column (3) of Table 2 and the dependent variable is logemployment in Rows [1]-[2] and [7]-[8], a dummy that takes value of one in any given firm-yearn when there is alayoff in Rows [3]-[4] and [9]-[10], and the ratio of capital expenditures to assets at the start of the period in Rows[5]-[6] and [11]-[12]. All variable definitions are in Appendix A. We only report estimates of the Bind coefficient andomit estimates of firm controls from the table for brevity (available upon request). Panel A presents the results for theentire sample. Panel B only uses firm-year observations in which firms are close to violating the covenant, defined as anarrow range (±20%) around the covenant threshold ("Discontinuity sample"). These samples are split between bottomand top quartiles of (year-prior) values of the following ex-ante industry-level proxies union membership (Column(1)) and coverage (Column (2)); the average industry ratio of employees to assets (Column (3)) and SG&A to assets(Column (4)), the Herfindahl-Hirschman Index (HHI) (Column (5)) and the degree of import penetration (Column (6)).Standard errors robust to heteroskedasticity and within-firm serial correlation appear below point estimates. Levels ofsignificance are indicated by *, **, and *** for 10%, 5%, and 1% respectively.

Panel A: Entire SampleUnionization Labor Intensity & Flexibility Competition

(1) (2) (3) (4) (5) (6)Member- Coverage Labor- Labor Adj HHI Import Pe-

ship Capital Ratio Costs netrationLog(Employment)[1] Q1 -0.223∗∗∗ -0.270∗∗∗ -0.066∗ -0.216∗∗∗ -0.106∗ -0.212∗∗∗

(0.082) (0.094) (0.037) (0.043) (0.063) (0.065)[2] Q4 -0.074 -0.075 -0.269∗∗∗ -0.061 -0.257∗∗∗ -0.141∗∗

(0.047) (0.047) (0.044) (0.049) (0.055) (0.065)Layoffs, Probit[3] Q1 0.134∗∗∗ 0.166∗∗∗ 0.029∗∗ 0.131∗∗∗ 0.035∗∗ 0.098∗∗∗

(0.033) (0.038) (0.016) (0.017) (0.017) (0.036)[4] Q4 0.025 0.012 0.160∗∗∗ 0.030∗ 0.138∗∗∗ 0.033

(0.018) (0.014) (0.016) (0.016) (0.014) (0.024)Investment[5] Q1 -0.002 -0.003 -0.013∗∗ -0.003 -0.002 -0.014∗∗

(0.004) (0.004) (0.006) (0.003) (0.007) (0.006)[6] Q4 -0.010∗∗ -0.009∗∗∗ -0.006∗∗ -0.017∗∗∗ -0.013∗∗∗ -0.002

(0.004) (0.004) (0.003) (0.007) (0.004) (0.004)Panel B: Discontinuity Sample

Log(Employment)[7] Q1 -0.213∗∗∗ -0.265∗∗∗ -0.056 -0.244∗∗∗ -0.098 -0.213∗∗

(0.078) (0.095) (0.058) (0.059) (0.131) (0.105)[8] Q4 -0.031 -0.056 -0.265∗∗∗ -0.062 -0.223∗∗∗ -0.131

(0.069) (0.058) (0.095) (0.080) (0.071) (0.095)Layoffs, Probit[9] Q1 0.139∗∗∗ 0.180∗∗∗ 0.001 0.140∗∗∗ 0.016 0.112∗∗∗

(0.037) (0.041) (0.029) (0.021) (0.023) (0.051)[10] Q4 0.014 0.001 0.180∗∗∗ 0.045 0.137∗∗∗ 0.047

(0.024) (0.029) (0.041) (0.035) (0.019) (0.037)Investment[11] Q1 -0.002 -0.003 -0.012∗∗ -0.001 -0.005 -0.015∗∗

(0.004) (0.004) (0.005) (0.005) (0.007) (0.006)[12] Q4 -0.011∗∗ -0.012∗∗ -0.003 -0.017∗∗ -0.013∗∗∗ -0.001

(0.005) (0.005) (0.004) (0.008) (0.005) (0.006)

37

Table 5: Loan Covenant Violations and Employment in Good and Bad Times

This table presents regression results of employment on a covenant violation measure ("Bind") and controls for differentsub-sample splits of the data based on proxies for macroeconomic conditions. The model specification is the one withfirm fixed effects, controls, and splines as in Column (3) of Table 2 and the dependent variable is log employment inRows [1]-[2] and [7]-[12], a dummy that takes value of one in any given firm-yearn when there is a layoff in Rows[3]-[4], and the ratio of capital expenditures to assets at the start of the period in Rows [5]-[6]. All variable definitionsare in Appendix A. We only report estimates of the Bind coefficient and omit estimates of firm controls from the tablefor brevity (available upon request). Panel A presents the results for the entire sample, which is split based on severalproxies between good (Columns (1) to (3) and bad (Columns (4) to (6)) times. Panel B further stratifies the samplebased on credit rating status (Rows [7] and [8]), and industry union membership (Rows [9] and [10]). Standard errorsrobust to heteroskedasticity and within-firm serial correlation appear below point estimates. Levels of significance areindicated by *, **, and *** for 10%, 5%, and 1% respectively.

Panel A: Entire SampleBad Times Good Times

(1) (2) (3) (4) (5) (6)Industry NBER The Great Industry High Tech The Great

Downturn Recession Recession Expansion Boom ModerationLog(Employment)[1] Yes -0.246∗∗∗ -0.290∗∗∗ -0.424∗∗∗ -0.057 -0.023 -0.088∗∗∗

(0.037) (0.057) (0.099) (0.041) (0.068) (0.028)[2] No -0.109∗∗∗ -0.089∗∗∗ -0.089∗∗∗ -0.239∗∗∗ -0.230∗∗∗ -0.194∗∗∗

(0.024) (0.020) (0.020) (0.025) (0.067) (0.030)Layoffs, Probit[3] Yes 0.198∗∗∗ 0.157∗∗∗ 0.198∗∗∗ 0.019 0.053 0.064∗∗∗

(0.024) (0.028) (0.059) (0.024) (0.060) (0.015)[4] No 0.053∗∗∗ 0.058∗∗∗ 0.095∗∗∗ 0.146∗∗∗ 0.167∗∗∗ 0.132∗∗∗

(0.012) (0.010) (0.009) (0.012) (0.045) (0.014)Investment[5] Yes -0.009∗∗∗ -0.009∗∗ -0.012∗∗ -0.006 -0.009∗∗ -0.008∗∗∗

(0.003) (0.004) (0.005) (0.005) (0.004) (0.002)[6] No -0.007∗∗∗ -0.006∗∗∗ -0.005∗∗∗ -0.010∗∗∗ -0.008∗∗ -0.007∗∗∗

(0.002) (0.002) (0.001) (0.002) (0.004) (0.002)Panel B: Row 1 By Firm and Industry Characteristics

By Firm Credit Rating Status[7] Rated -0.112∗∗ -0.159∗∗∗ -0.083 -0.046 -0.002 -0.022

(0.048) (0.061) (0.200) (0.093) (0.102) (0.040)[8] Not Rated -0.315∗∗∗ -0.354∗∗∗ -0.709∗∗∗ -0.066 -0.036 -0.086∗∗∗

(0.086) (0.077) (0.201) (0.048) (0.066) (0.032)

By Industry Unionization (Union Membership)[9] Q1 -0.340∗∗∗ -0.367∗∗∗ -0.612∗∗∗ -0.091 -0.105 -0.102∗∗

(0.094) (0.093) (0.153) (0.064) (0.083) (0.044)[10] Q4 -0.148∗ -0.188∗∗ 0.203 -0.046 -0.001 -0.023

(0.078) (0.078) (0.123) (0.059) (0.091) (0.031)

38

Table 6: Loan Covenant Violations and Employment: Robustness Analysis

In this table, we check for robustness of the impact of violations on employment presented in Table 2to using alternative specifications (Panel A), alternative samples and definitions of covenant violations(Panel B), and to including additional controls (Panels C and D). In all robustness checks, the startingmodel specification is the one with firm fixed effects, controls, and splines as in Column (3) of Table 2 andthe dependent variable is log employment. We only report estimates of the covenant violation coefficientand omit estimates of firm controls from the table for brevity (available upon request). Columns 1 and3 present the results for the entire sample. Columns 2 and 4 only use firm-year observations in whichfirms are close to violating the covenant, defined as a narrow range (±20%) around the covenant threshold("Discontinuity sample"). Panel A reports results from the following specifications: a median (quantile)regression specification in Row [1]; a specification that adds a lagged dependent variable in Row [2]; andspecifications that add one more lag and two leads of Bind in Rows [3] and [4], respectively. Panel B showsresults for: using an alternative definition of Bind based on the violation dummies hand-collected from SECfilings by Nini, Smith, and Sufi (2012) in Row [5]; using a broader definition of Bind that includes the fullset of covenants that have threshold information available in Dealscan in Row [6]; using a smaller samplethat excludes observations when there is a divestiture of assets in Row [7]; and using a smaller sample thatexcludes the years of the financial crisis in Row [8]. Panels C and D present results for specifications thatinclude the following additional controls: investment in Row [9]; a dummy for whether the firm undergoesa divestiture of assets in any given year in Row [10]; 2nd- and 5th-order non-liner splines of the distancefrom the covenant threshold in Rows [11] and [12], respectively; book leverage in Row [13]; Tobin’s Q inRow [14]; Altman’s Z-score in Row [15]; and discretionary accruals in Row [16]. All variable definitionsare in Appendix A. Standard errors robust to heteroskedasticity and within-firm serial correlation appearbelow point estimates. Levels of significance are indicated by *, **, and *** for 10%, 5%, and 1% respectively.

Robustness Estimated Coeff, Robustness Estimated Coeff,Test log(Employment) Test log(Employment)

Entire Disconti- Entire Disconti-Sample nuity Sample nuity

(1) (2) (3) (4)

Panel A: Alternative Specifications Panel C: Additional ControlsControlling for:

[1] Median (quantile) regression -0.206∗∗∗ -0.218∗∗∗ [9] Investment -0.175∗∗∗ -0.126∗∗∗

(0.030) (0.048) (0.021) (0.032)[2] Include lagged dependent -0.133∗∗∗ -0.106∗∗∗ [10] Divestitures -0.176∗∗∗ -0.131∗∗∗

(0.014) (0.022) (0.021) (0.032)[3] Include two lags of Bind -0.152∗∗∗ -0.116∗∗∗ [11] 2-nd Splines -0.171∗∗∗ -0.126∗∗∗

(0.039) (0.041) (0.021) (0.030)[4] Include two leads of Bind -0.151∗∗∗ -0.115∗∗∗ [12] 5-th Splines -0.169∗∗∗ -0.117∗∗∗

(0.028) (0.036) (0.021) (0.031)

Panel B: Alternative Covenants and Samples Panel D: Other Additional ControlsControlling for:

[5] Use violations dummy from -0.120∗∗∗ n.a. [13] Leverage -0.172∗∗∗ -0.142∗∗∗

Nini, Smith, and Sufi (2012) (0.024) n.a. (0.022) (0.030)[6] Include all other covenants -0.070∗∗∗ -0.092∗∗∗ [14] Tobin’s Q -0.175∗∗∗ -0.132∗∗∗

(0.011) (0.027) (0.023) (0.032)[7] Exclude divesting firm-years -0.162∗∗∗ -0.113∗∗∗ [15] Z-Score -0.163∗∗∗ -0.102∗∗∗

(0.022) (0.028) (0.022) (0.031)[8] Exclude financial crisis years -0.163∗∗∗ -0.116∗∗∗ [16] Accruals -0.164∗∗∗ -0.128∗∗∗

(0.023) (0.033) (0.023) (0.032)

39

Table 7: Union Election Sample: Summary Statistics

This table presents summary statistics (means and medians) for our merged Union (NLRB)-Dealscan (DS)-Compustat sample, which consists of 3,814 observations for nonfinancial firms between 1985 and 2010corresponding to loans that have union representation election information in NLRB for firms in Compustatand loan pricing information in Dealscan one year after the union election event (Column 1 and 2, PanelA). For the sake of comparison, Columns 3 and 4 (Panel A) report summary statistics (means and medians)for the Other Dealscan-Compustat sample, which consists of the remaining observations in the mergedDealscan-Compustat sample for the same period that have no matching information in NLRB. Panel Breports summary statistics (means and medians) for two sub-samples of the Union (NLRB)-Dealscan (DS)-Compustat sample, based on whether the representation election results in a win or a loss for the union.Panel C reports summary statistics (means and medians) for two more sub-samples of the Union (NLRB)-Dealscan (DS)-Compustat sample, based on whether the representation election results in a "close" win ora "close" loss for the union and with "closeness" defined as a narrow range (a vote share range of ±5%)around the majority (50%) threshold needed for the union to win representation ("Discontinuity sample").All variable definitions are in Appendix A.

Panel A: Union (NLRB)-Dealscan (DS)-Compustat SampleNLRB-DS-Compustat Other DS-Compustat

Mean Median Mean Median(1) (2) (3) (4)

Union Election Results and Other Election Characteristics:Union Win 0.36 0 n.a. n.a.Union Election Size 268.5 141.0 n.a. n.a.Union Vote Share 0.46 0.43 n.a. n.a.

Loan Spreads After Union Elections:Loan Spread, Year=+1 (bps) 180 150 223 212Loan Spread, Year=+2 (bps) 181 150 223 212Loan Spread, Year=+1,+2 (bps) 181 150 223 212

Loan Spreads & Firm Characteristics Before Union Elections:Log(Assets) 9.0 9.2 6.6 6.5M/B 1.6 1.3 1.6 1.3Rated Dummy 0.58 1 0.55 0Loan Spread, Year=-1 (bps) 179 125 223 212Panel B: Difference in Pre-Election Characteristics between All Union Wins vs. Losses

Union Wins Union LossesMean Median Mean Median

(1) (2) (3) (4)Loan Spreads & Firm Characteristics Before Union Elections:Log(Assets) 8.9 9.2 9.0 9.3M/B 1.5 1.3 1.6 1.4Rated Dummy 0.57 1 0.59 1Loan Spread, Year=-1 (bps) 184 150 176 125Panel C: Difference in Pre-Election Characteristics between Close Union Wins vs. Losses

Close Union Wins Close Union LossesMean Median Mean Median

(1) (2) (3) (4)Loan Spreads & Firm Characteristics Before Union Elections:Log(Assets) 9.1 9.2 9.1 9.2M/B 1.6 1.3 1.6 1.3Rated Dummy 0.58 1 0.58 1Loan Spread, Year=-1 (bps) 178 125 175 125

40

Table 8: Union Elections and Loan Pricing: Baseline Analysis

This table presents results for tests of differences in means of loan spreads after union election events de-pending on whether the election outcome was a win or a loss for the union. Columns (1) to (4) refer toloan spreads one year after the election and Columns (5) to (8) are for spreads two years after the elec-tion. For each spread, Panels A reports results for the entire sample (Columns (1) and (5)) and varioussub-samples that exclude elections involving, in turn, operating subsidiaries (Columns (2) and (6)), fewerthan 150 employees (Columns (3) and (7)), and those involving both fewer than 150 employees and invest-ment grade-rated firms (Columns (4) and (8)). Panel B only uses observations involving "close" elections,defined as a narrow range (a vote share range of±5%) around the majority (50%) threshold needed for theunion to win representation ("Discontinuity sample"). Panel C stratifies the sample based on the numberof employees involved in each election. All variable definitions are in Appendix A. Standard deviationsappear in square brackets below mean loan spreads and p-values are below the difference in mean loanspreads. Levels of significance are indicated by *, **, and *** for 10%, 5%, and 1% respectively.

Panel A: Entire SampleLoan Spread, Year=+1 Loan Spread, Year=+2

(1) (2) (3) (4) = (3)+ (5) (6) (7) (8) = (7)+All Exclude Exclude Exclude All Exclude Exclude Exclude

Subs Small Inv Grade Subs Small Inv Grade

Union Win 189.7 204.1 214.4 250.1 188.6 200.7 207.9 264.1[144.0] [145.5] [155.4] [155.5] [159.3] [138.2] [187.3] [194.9]

Union Loss 168.9 163.0 161.1 191.1 153.5 156.0 149.5 198.4[128.8] [121.7] [139.1] [150.5] [129.9] [129.5] [139.1] [153.9]

Difference 20.8∗∗∗ 41.1∗∗∗ 53.4∗∗∗ 59.0∗∗∗ 35.1∗∗∗ 44.7∗∗∗ 58.4∗∗∗ 65.6∗∗∗p-value (0.000) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000)

Observations 3,814 2,382 1,652 734 3,811 2,366 1,635 720

Panel B: Discontinuity Sample

Union Win 236.5 244.4 265.7 295.1 226.7 252.9 213.9 259.5[164.9] [186.3] [199.9] [204.6] [149.5] [149.3] [142.0] [133.3]

Union Loss 167.2 135.7 125.9 141.8 141.6 151.0 119.5 140.1[146.5] [114.9] [101.7] [110.8] [106.9] [120.1] [102.7] [140.1]

Difference 69.2∗∗∗ 108.7∗∗∗ 139.7∗∗∗ 153.3∗∗∗ 85.1∗∗∗ 101.9∗∗∗ 94.4∗∗∗ 119.4∗∗∗p-value (0.000) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000)

Observations 470 276 232 102 511 301 227 100

Panel C: Loan Spread, Year=+1 by Union Election Size(1) (2) (3) (4) (5) (6) (7) (8)

N≥100 N≥150 N≥200 N≥250 N≥300 N≥350 N≥400 N≥450

Union Win 190.7 214.4 215.9 226.4 232.1 240.5 240.8 253.0[146.2] [155.4] [171.4] [182.2] [190.2] [200.2] [201.1] [213.5]

Union Loss 167.9 161.1 162.2 151.5 149.5 155.4 153.7 142.1[138.9] [139.1] [138.1] [143.6] [147.1] [152.4] [159.8] [119.4]

Difference 22.8∗∗∗ 53.4∗∗∗ 53.7∗∗∗ 74.9∗∗∗ 82.6∗∗∗ 85.0∗∗∗ 87.1∗∗∗ 110.9∗∗∗p-value (0.002) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000)

Observations 2,466 1,652 1,204 913 736 601 509 447

41

Table 9: Union Elections and Loan Pricing: Matched-Sample Analysis

This table presents results for t-tests of differences in means of average excess loan spreads in the two yearsafter union election events depending on whether the election outcome was a win or a loss of for the union.Average excess loan spreads are defined as the difference between loan spreads and the average loan spreadfor a portfolio of matching loans. Columns (1) to (4) of Panel A refer to average excess loan spreads overa portfolio of loans matched based on year, industry, and firm size (deciles), while Columns (5) to (8) ofPanel B are for average excess loan spreads over a portfolio of loans matched based on year, industry, andfirm growth opportunities (Market to book ratio deciles). For each spread, we report results for the entiresample (Columns (1) and (5)) and various sub-samples that exclude elections involving, in turn, subsidiaries(Columns (2) and (6)), fewer than 150 employees (Columns (3) and (7)), and those involving both fewer than150 employees and investment grade-rated firms (Columns (4) and (8)). Columns (1) to (4) of Panel C referto average excess loan spreads over a portfolio of loans matched based on year, industry, and firm creditratings, while Columns (5) to (8) of Panel D are for average excess loan spreads over a portfolio of loansmatched based on year, industry, and loan spreads (deciles) one year before the election. For each spread,we again report results for the entire sample (Columns (1) and (5)) and various sub-samples that excludeelections involving, in turn, subsidiaries (Columns (2) and (6)), fewer than 150 employees (Columns (3) and(7)), and those involving both fewer than 150 employees and investment grade-rated firms (Columns (4)and (8)). All variable definitions are in Appendix A. Standard deviations appear in square brackets belowmean loan spreads and p-values are below the difference in mean loan spreads. Levels of significance areindicated by *, **, and *** for 10%, 5%, and 1% respectively.

A. Year, Industry, & Size Matched B. Year, Industry, & Growth Opp. Matched(1) (2) (3) (4) = (3)+ (5) (6) (7) (8) = (7)+All Exclude Exclude Exclude All Exclude Exclude Exclude

Subs Small Inv Grade Subs Small Inv Grade

Union Win 24.0 23.6 38.2 139.4 -26.2 -10.1 -27.1 124.6[121.3] [120.8] [121.1] [140.4] [134.0] [132.2] [135.0] [131.6]

Union Loss 8.7 -2.1 4.7 76.9 -42.7 -51.0 -58.9 34.1[111.6] [108.2] [115.4] [155.3] [121.1] [115.7] [126.6] [165.1]

Difference 15.3∗∗∗ 25.8∗∗∗ 33.4∗∗∗ 62.5∗∗∗ 16.5∗∗∗ 41.0∗∗∗ 31.8∗∗∗ 90.5∗∗∗p-value (0.001) (0.000) (0.000) (0.000) (0.001) (0.000) (0.000) (0.000)

Observations 3,122 1,845 1,378 606 3,124 1,844 1,376 605

C. Year, Industry, & Ratings Matched D. Year, Industry, & Prior Spread Matched(1) (2) (3) (4) = (3) (5) (6) (7) (8) = (7)All Exclude Exclude + Below All Exclude Exclude + Below

Subs Small Inv Grade Subs Small Inv Grade

Union Win 10.9 9.1 26.9 39.0 19.4 12.9 26.3 140.3[97.4] [98.4] [120.9] [151.8] [103.9] [106.0] [111.5] [149.6]

Union Loss -5.1 -10.7 -2.3 -22.1 2.2 -6.7 -2.9 59.1[93.3] [90.4] [95.0] [135.9] [92.3] [84.4] [96.8] [165.3]

Difference 16.0∗∗∗ 19.9∗∗∗ 29.2∗∗∗ 61.1∗∗∗ 17.2∗∗∗ 19.6∗∗∗ 29.3∗∗∗ 81.2∗∗∗p-value (0.000) (0.000) (0.000) (0.000) (0.001) (0.000) (0.000) (0.001)

Observations 3,113 1,840 1,372 604 3,106 1,829 1,376 605

42

Figure 1: Loan Covenant Violations and Employment

The sample consists of 11,536 firm-year observations for nonfinancial firms between 1994 and 2010 corre-sponding to firms that have at least one private loan found in Dealscan with a covenant that restricts currentratio or net worth to lie above a certain threshold. This figures shows average percentage annual changesin the number of employees in event time leading to and after the year when a covenant violation occurs.

Figure 2: Unionization Elections and Loan Spreads

The sample consists of 3,814 observations for nonfinancial firms between 1985 and 2010 corresponding toloans that have union representation election information in NLRB for firms in Compustat and loan pricinginformation in Dealscan one year after the union election event. This figures plots mean loan spreads foreach of ten equally-spaced bins of the data sorted on values of the union vote share variable, with thevertical line denoting the 50% vote threshold.

43